Reviewer3 (AI review)

October 1, 2026

AI Review (reviewer3.com)

Comments (5)

1. Inconsistent comparison of weighted and unweighted statistics — Editorial

or more publishers, giving 99.05% single-publisher bags (99.02% sales-weighted). The 6.78-point difference from the fragment statistic illustrates the magnitude of the population-selection effect induced by unverifiable completeness. All journey-level inference below uses the complete subset.

In Section 2, the author states that the selection effect is illustrated by a '6.78-point difference from the fragment statistic'. This value is obtained by subtracting the weighted fragment statistic (92.27% 'Single sales' in Table 1) from the unweighted complete statistic (99.05% '1-pub. conv.' in Table 1). This inconsistent comparison is repeated in Section 6, which contrasts '92.27-to-99.05'. To measure the selection effect accurately, the paper should compare equivalent metrics: either the unweighted statistics (99.05% vs 92.19%, a 6.86% difference) or the weighted statistics (99.02% vs 92.27%, a 6.75% difference).

2. Single-day temporal truncation bias — Minor

Four local files were discovered; two are empty and two day- 15 files contain 430,834 and 410,100 rows. These are row shards, not user partitions. Exactly 35,065

The analysis uses only the day-15 files of the CriteoPrivateAds dataset. Because user journeys in digital advertising often span multiple days, analyzing only a single 24-hour window naturally truncates any journey that began on previous days. This temporal truncation directly causes many journeys to be flagged as incomplete (e.g., not starting at display_order=1), leading to their exclusion under the complete-bag rule. Since multi-publisher journeys are typically longer and take more time to develop, they are disproportionately affected by this temporal truncation, further exacerbating the selection bias. Journeys should be reconstructed across the full multi-day dataset to capture complete multi-day journeys.

3. CriteoPrivateAds complete-bag selection bias — Critical

use three. The 92.27-to-99.05 contrast is not a corrected measurement but a selection effect: the completeness filter retains systematically shorter journeys, and the excluded 48.8% are 86.83% single-publisher, so the two numbers describe different populations. Under the declared 0.01 margin,

An extremely restrictive complete-bag filtering rule is applied to CriteoPrivateAds, discarding 48.8% of the sequences. While the text acknowledges that this filter retains systematically shorter journeys and that the excluded 48.8% contain a much higher proportion of multi-publisher journeys (13.17% vs 0.95% in the retained set), the paper still concludes that the dataset itself fails to support multi-channel journeys and that attribution models are indistinguishable. By discarding the vast majority of multi-publisher journeys—which are naturally longer and more likely to span shards or have gaps—the analysis artificially creates a subset that is 99.05% single-publisher. This indistinguishability is entirely an artifact of the filtering process, not a property of the underlying dataset. The analysis should be performed on the full dataset or a representative sample without applying a filter that systematically discards multi-publisher journeys.

4. Arbitrary distinguishability margin — Major

We declare a distinguishability margin δ = 0 . 01 TV, one percentage point of aggregate credit. Two

A distinguishability margin of δ = 0.01 TV (one percentage point of aggregate credit) is declared without providing any empirical or theoretical justification for why this threshold represents a material difference. In large-scale digital advertising, even a fraction of a percent shift in budget allocation can represent significant financial and operational impact. The choice of this threshold should be justified, or a sensitivity analysis should be presented showing how the conclusions change with different choices of δ.

5. Criteo Attribution reconstruction key error — Critical

events [4]. We join only rows sharing all three fields. Every event contains one raw campaign. Collapsing instead to one path per user would

The reconstruction of journeys in the Criteo Attribution dataset is performed by joining only rows that share the exact same (user, conversion_id, conversion_timestamp). This represents a fundamental misunderstanding of the dataset's schema. In this dataset, prior touchpoints (clicks) that did not directly convert have conversion = 0 and do not possess a conversion_id or conversion_timestamp. By requiring all joined rows to share the conversion_id, the reconstruction method systematically excludes all prior touchpoints in the user's history, leaving only the single converting touchpoint. This mathematically guarantees that every reconstructed journey contains exactly one campaign, artificially manufacturing the single-campaign result and invalidating the conclusion that the dataset does not support multi-channel journeys. To fix this, journeys should be reconstructed by grouping by user and including all touchpoints prior to the conversion timestamp.

xPeerd (AI review)

October 1, 2026

AI Review (xPeerd — DAReview)

Summary

This manuscript, “When Shapley Wins by Construction: Auditing Proxy-Target Attribution Benchmarks,” argues that offline multi-touch attribution benchmarks can become uninformative for two main reasons: the reconstructed journeys may not actually support a meaningful multi-channel attribution problem, and the benchmark target may be mathematically coupled to a candidate method, making good performance tautological rather than empirical. The paper’s central strengths are its sharply stated benchmark-validity framework with three conditions—journey validity, empirical distinguishability, and target independence—and its effort to ground these claims in two public attribution datasets and a formal identity involving coverage-game Shapley outputs. The abstract and Section 1 clearly articulate the contribution and stakes of the work, and the manuscript is commendably explicit about several limitations, including deterministic completeness filtering and lack of population power claims.

The principal weaknesses are narrower scope and external-validity limitations than the framing initially suggests, together with several places where the rhetoric risks overgeneralizing from a very sparse empirical base. In particular, the reported complete-bag evidence rests on only 25 multi-publisher converting bags out of 2,619 complete converting bags, and the paper itself notes that the retained subset is not a random sample and that excluded data may differ in unknown ways. The theoretical point about target dependence appears stronger than the empirical benchmark audit, but the manuscript sometimes blends those levels in ways that could invite overinterpretation.

Potential Major Revisions

1. Clarify the manuscript’s effective contribution hierarchy and avoid overstating the empirical generality.

The strongest result in the paper is the theoretical benchmark-design warning in Section 4, especially the statement that “if q is scored against the same constructed T1, zero TV is fixed by design” and that this is a “benchmark-design diagnostic.” However, the manuscript’s title, abstract, and opening framing can be read more broadly as an audit of offline attribution benchmarks as such. The abstract states, “Together these results show how insufficient journey support and target dependence can make offline attribution comparisons appear more informative than the underlying benchmark permits,” which is defensible, but because the empirical portion is so dataset-specific, I think the manuscript should more explicitly rank its contributions: first, a formal design warning; second, a narrow empirical audit of two public datasets.

This matters because the empirical evidence is highly constrained. The manuscript reports that in the retained complete-bag subset, “Only 25/2,619 complete converting bags (0.9546%) are genuinely multi-publisher,” and “none [of the complete converting bags] use three.” That is a striking finding, but it is also exactly the sort of narrow support that limits how far one can generalize about attribution benchmarking beyond these releases and reconstruction rules. I recommend revising the abstract, introduction, and conclusion so they state more plainly that the empirical findings are a case-specific failure analysis rather than evidence that most offline attribution comparisons are similarly compromised.

2. Strengthen the justification for the distinguishability threshold and show robustness to alternative margins.

Section 3 declares “a distinguishability margin δ = 0.01 TV, one percentage point of aggregate credit,” and then treats methods as distinguishable only if both point TV and the lower bound of a paired bootstrap interval exceed that value. This is coherent internally, but the choice of 0.01 functions as a substantive decision criterion, not a merely technical parameter. Since the manuscript’s main empirical conclusion is that “Under the declared 0.01 margin, the complete-bag data do not distinguish the nine eligible output vectors,” the strength of that conclusion depends materially on the threshold.

I think the paper needs either a field-grounded justification for why 1 percentage point of aggregate credit is operationally meaningful, or a sensitivity analysis over several plausible margins. Otherwise, readers may reasonably ask whether the negative result is an artifact of a threshold selected post hoc or one whose operational meaning is underdeveloped. This is especially important because one reported paired-bootstrap interval for first-versus-last touch reaches above δ at the upper bound while remaining below it at the lower bound, indicating the conclusion hinges on the inferential rule. A margin-robustness figure or table would materially improve the manuscript’s reproducibility and interpretability.

3. More sharply separate what is proven, what is source-inspected, and what is inferred from repository behavior.

The manuscript is appropriately careful in some places, for example stating that “Source inspection establishes a coverage-game implementation in the pinned eeghor/mta revision [14], but does not establish equal split as an evaluation target.” That sentence is strong and appropriately cautious. However, elsewhere the exposition moves quickly between theorem, implementation agreement, and benchmark interpretation. For instance, the paper states, “The actual Rust allocator agrees with the independent output a to 2.78 × 10−17 maximum channel error,” and then discusses grouping effects and target dependence in close proximity.

I recommend restructuring Section 4 into explicit subsections such as: formal identity, implementation verification, and interpretive implications. That would reduce the risk that readers conflate proof of the identity with proof that published benchmark practices actually instantiate the problematic target coupling. The paper’s own caution that its result should not be read “as an estimate of how often this pairing occurs in published work” is important and should appear earlier and more prominently.

4. Address possible concerns about selection effects more directly and quantitatively.

The manuscript acknowledges a major limitation: “The complete subset is defensible for a local census but is not a random sample of the full release. The excluded 48.8% may differ in unknown ways.” This is a serious issue because the central empirical claims about journey validity and distinguishability are made on that retained subset. The paper does note that the completeness filter “retains systematically shorter journeys,” and that fragment and complete rows describe different populations.

I think the paper should go further here. At minimum, it should provide a more structured characterization of the retained versus excluded populations using whatever non-outcome-defining covariates are available, even if only descriptively. For example, since the rule is based only on order values and shard provenance, a table comparing simple observable properties across retained and excluded records could help readers assess the plausibility of the retained subset as an audit substrate. Without that, the current empirical section risks being read as stronger evidence about the underlying dataset than the manuscript itself ultimately allows.

5. Reconsider the epistemic force of claims derived from extremely sparse multi-publisher support.

The manuscript argues that the benchmark does not support ranking attribution rules because there is too little heterogeneous multi-publisher support. That is plausible and likely correct on the reported evidence. But some wording should be tightened to reflect just how sparse the evidence is. Section 3 reports that only 25 complete converting bags are multi-publisher and that these account for 37 of 3,775 sales. With support that thin, the manuscript should explicitly discuss whether even exact aggregate TV comparisons are substantively meaningful, beyond serving as a negative diagnostic.

In other words, if the data support for the attribution problem is nearly degenerate, then the paper is not only showing non-distinguishability among methods; it may also be showing that the benchmark scarcely instantiates the intended task at all. That distinction is implicit in Section 1’s condition (C1), but making it explicit would sharpen the paper’s conceptual contribution. I suggest revising the discussion to distinguish “failure to rank methods” from “failure of the dataset to instantiate a meaningful multi-touch attribution setting.”

6. Expand fraud/paper-mill screening conclusion: low concern, but some rhetoric should be normalized.

I do not see strong signs of fabrication or paper-mill traits. The manuscript is technically coherent, cites prior literature specifically, states limitations candidly, and includes reproducibility-oriented details such as input hashes, executed commands, seeds, environment versions, and source commits. That said, there is a stylistic pattern of emphatic positioning—for example, “When Shapley Wins by Construction” and repeated cautionary framing—that may encourage a stronger reading than the narrow empirical support can bear. This is not evidence of misconduct; rather, it is a presentation issue. I would advise moderating some headline rhetoric so that the scope of the evidence and the scope of the warning remain tightly aligned.

Potential Minor Revisions

1. Formatting and layout issues

The PDF text suggests page-flow and layout problems. For example, “Preprint. arXiv:submit/8137349 [cs.LG] 27 Sep 2026Table 1” appears to run the preprint footer directly into the table caption, indicating insufficient spacing or a rendering problem on page 1. Likewise, “2Table 2” and “3credit-vector distance” appear in the extracted text, suggesting page-number or line-break collisions around page transitions. These should be corrected in the source file before submission.

2. Notational clarity

Equation references and notation are generally careful, but some distinctions could be made easier to track. In Section 4, the paper introduces Tw, T1, q, a, g(A), and ϕc(g) in close succession. Although mathematically manageable for a technical reader, a compact notation table would reduce cognitive load and improve accessibility. This is particularly advisable because a major argument hinges on the distinction between q and a: “The identity concerns q, not allocated a.”

3. Terminological consistency

The manuscript alternates across several closely related descriptors: “single raw campaign,” “single raw publisher,” “multi-channel,” and “multi-publisher.” Compare, for instance, “Every event contains one raw campaign” in the Criteo Attribution discussion with “99.05% single-publisher bags” in the PrivateAds discussion. These distinctions may be technically justified, but they should be explicitly harmonized so readers do not confuse campaign-level and publisher-level claims.

4. Table interpretation assistance

Table 2 is important for the paper’s empirical claim, but its practical interpretation is not as transparent as it could be. The manuscript reports values such as 0.1408, 0.1401, and 0.1419 against Tw, and grouped-channel values around 0.046. A brief sentence under the table or in the main text clarifying what constitutes a “small” versus “large” distance relative to the paper’s inferential objective would help. Similarly, Appendix Table 3 would benefit from a short interpretive note reminding readers that all entries are below the declared 0.01 margin.

5. More explicit section cross-referencing

Section 1 says “Section 2 shows,” “Section 3 shows,” and “Section 4 shows,” which is helpful. But later sections would benefit from more backward cross-references, especially when discussing the implications of completeness filtering and target dependence. For example, the conclusion could explicitly point back to (C1)–(C3) when summarizing what failed and how. This would tighten argumentative coherence.

6. Minor language edits

A few sentences are dense enough to merit stylistic simplification. For example, “Fragment reconstruction is not a valid journey-level estimator, so we report neither it nor any fragment-based TV as a result” is precise but compressed. Similarly, “Low proxy-target TV here describes benchmark construction and data support, not recovered causal credit” is accurate but could be unpacked slightly for clarity. These are not grammatical errors so much as readability improvements.

7. AI-content analysis

Estimated AI-generated content: low-to-moderate probability of AI-assisted polishing, but not strong evidence of predominantly AI-generated authorship.

Rationale: the manuscript is unusually compressed, highly regular in sentence construction, and rhetorically systematic in a way that can be consistent with either expert technical prose or AI-assisted editing. However, the document also contains field-specific technical distinctions, careful limitation statements, equation-linked reasoning, source-inspection details, and non-generic empirical caveats that are less characteristic of low-effort AI-generated papers.

Estimated percentage of AI-generated content: 15–35%.

Highlighted potentially AI-assisted sections:

• The abstract and opening framework in Section 1, due to highly polished symmetry in the two-failure-mode setup and three-condition enumeration.
• Portions of the conclusion, especially compact high-density synthesis such as “Low proxy-target TV here describes benchmark construction and data support, not recovered causal credit.”

Assessed epistemic impact: limited if AI assistance was used for wording or compression only; more serious if any proofs, empirical interpretations, or literature claims were machine-generated without full verification. Based on the text alone, I do not see obvious hallucinated references or incoherent technical insertions. The epistemic risk appears lower than in typical AI-generated manuscripts, but the author should still manually verify all claims, especially around the literature-scope distinctions and theorem interpretation.

Recommendations

1. Reframe the manuscript so the formal benchmark-design warning is clearly the primary contribution and the empirical dataset audit is clearly a bounded case study.
2. Add robustness analysis for the distinguishability threshold δ, ideally across multiple operationally interpretable margins.
3. Restructure Section 4 to separate theorem, implementation validation, and benchmark-design implications.
4. Add a descriptive retained-versus-excluded comparison to better contextualize the completeness filter and its selection effects.
5. Tighten claims about what the empirical data can support, especially given that only 25 complete converting bags are multi-publisher.
6. Improve PDF layout and spacing issues before submission, particularly around page breaks, captions, and footers.
7. Add a notation table and harmonize campaign/publisher/channel terminology.
8. Preserve the current reproducibility strengths, as the manuscript’s explicit documentation of seeds, hashes, and clean checkouts is a notable asset.

Overall, I judge the manuscript to contain a meaningful and potentially publishable methodological caution, but in its current form I am skeptical of the breadth of its empirical claims relative to the narrowness of the audited support. The paper would be substantially strengthened by revisions that narrow its rhetorical scope, deepen robustness analysis, and more explicitly quantify the consequences of deterministic filtering.

XSci (AI review)

October 1, 2026

Referee Report

Manuscript: "When Shapley Wins by Construction: Auditing Proxy-Target Attribution Benchmarks" Field: Machine learning for computational advertising (cs.LG), with cooperative-game-theoretic and empirical-marketing methodology Recommendation: Major revision

Summary and Recommendation

This manuscript asks whether the standard offline evaluation setup in multi-touch attribution can support the comparisons routinely run on it. The authors propose three conditions for an informative comparison — that reconstructed journeys be complete and genuinely multi-channel, that the observed support be heterogeneous enough for competing allocation rules to produce materially different outputs, and that the evaluation target be mathematically independent of the candidate rule — and then audit two public datasets against them. Reconstructing Criteo Attribution by the triple (user, conversion_id, conversion_timestamp) yields 438,730 events, each reported to contain a single raw campaign. On CriteoPrivateAds, a deterministic rule combining display-order contiguity with shard provenance certifies 388,848 of 760,280 observed sequences, and among the 2,619 converting certified bags, 2,594 (99.05%) contain one raw publisher while none contain more than two. Across nine eligible attribution outputs the largest pairwise total variation distance is 0.0088053, below a declared margin of 0.01. Theorem 1 then establishes, via a known cooperative-game identity, that the Shapley vector of the coverage game in Equation (3) equals the count-weighted equal split T₁ exactly, so that scoring one against the other returns zero error by construction.

The research question is well chosen and the execution displays a methodological conscience that is uncommon in this literature. The refusal to collapse Criteo rows to one path per user, the insistence that fragment-level statistics be reported as reconstruction diagnostics rather than results, the explicit statement that completeness filtering is deterministic rather than probability sampling and therefore licenses no population inference, the frank acknowledgment that source inspection establishes a coverage-game implementation but not an equal-split evaluation target, and the observation in Appendix A that a valid Markov uncertainty analysis would require refitting on resampled converting and non-converting histories, all reflect genuine care. Theorem 1 is correct, cleanly proved by the standard unanimity-game argument, and honestly labelled as prior art whose novel element is the measurement reading placed upon it. I nonetheless recommend major revision. The paper's two empirical headlines rest on reconstruction choices presented as neutral readings of the data but which are in fact strong analytical commitments that bias toward the reported findings; the central negative result is inferred by accepting a null rather than by testing for equivalence, and the manuscript's own interval leaves the leading comparison unresolved; and the title's claim about Shapley is contradicted by the paper's own principal table. A paper arguing that benchmark construction can make comparisons appear more informative than they are must hold its own constructions to the same standard, and at present it does not.

Major Concern Category 1: Journey Reconstruction and Construct Validity

1.1 The Criteo event key appears finer than the dataset's documentation describes

Section 2 characterizes the triple (user, conversion_id, conversion_timestamp) as the Criteo Attribution release's "documented event key," and the single-campaign finding that follows is one of the paper's two empirical headlines, restated in the conclusion as "Criteo is entirely single-raw-campaign at its event key." This characterization warrants re-examination, because the official Criteo AI Lab release description does not describe a three-field key; it describes conversion_id as a unique identifier for each conversion, existing specifically so that timelines can be reconstructed if needed, with conversion_timestamp being an attribute of the conversion rather than a component of its identity. The authors' triple is therefore at least one field finer than the documented key. The consequence is not cosmetic: the same release description reports approximately 45,000 conversions, while the manuscript reports 438,730 events, nearly an order of magnitude more, and the discrepancy is nowhere reconciled. Either the official figure is imprecise or refers to a subset, in which case the reconciliation should be documented, or the triple is splitting single conversions into multiple events, in which case the finding that every event contains one raw campaign is substantially a consequence of the partition's fineness rather than a property of the data's multi-channel support. The manuscript is commendably alert to the mirror-image hazard, noting correctly that collapsing to one path per user would manufacture multi-channel journeys by gluing distinct conversions together, but it treats coarsening as the only error worth guarding against and never reports the intermediate construction that the documentation actually points toward. A short reconciliation reporting the raw-campaign histogram under all three candidate keys would either dissolve this concern entirely and strengthen the claim considerably, or would require the headline to be restated.

1.2 The channel construct is operationalized at a granularity where the central finding is close to forced

The journey census runs at raw-publisher granularity, with Table 2 recording 23,848 non-null publisher identifiers plus a missing category as the channel space. The attribution literature being audited — removal effects, Shapley allocations, position rules — conventionally operates over a channel space of order ten. The gap between twelve and 23,848 changes what the measured quantity means, because across that many identifiers the probability that a short converting sequence touches two distinct ones is small more or less by construction, and reporting that 99.05% of such sequences are singletons approaches reporting the cardinality of the identifier space. The manuscript supplies the evidence for this itself, which is to its credit but makes the framing harder to defend: Section 4 reports that grouping to the top eleven publishers plus an "other" bucket changes coverage-game-vector total variation by a factor of 3.07 and merges 11 of the 25 raw multi-publisher complete bags, and Table 2 shows the distance from the target falling from roughly 0.14 to roughly 0.046 under the same regrouping. The authors describe grouping as a material intervention, which is exactly right, and then do not follow through, since the census, the margin, and the entire Appendix A matrix are reported only at the granularity most favorable to the reported conclusion. A further consideration applies on the Criteo side, where the campaign field is widely treated as an advertiser proxy rather than a media-channel label; if that reading holds, every impression leading to a given advertiser's conversion is single-campaign by definition, and the finding restates the schema rather than observing the traffic.

1.3 The completeness rule certifies left-anchoring and contiguity but not completion

Equation (1) requires that the minimum display order be one, that the maximum minus the minimum plus one equal the sequence length, and that the user occupy a single row shard. The first two conditions establish that the observed sequence begins at the first display and contains no internal gaps. Neither establishes that the sequence ends where the journey ended. A user whose true sequence runs to nine displays but of whom the first five appear in the local files satisfies every clause and is certified complete. The rule is a left-truncation and internal-gap test rather than a completeness test, and the language of certification and provable completeness claims more than the stated criterion delivers. This is not hypothetical, because the manuscript reports the signature of exactly this failure when it observes in Section 6 that the filter retains systematically shorter journeys. Compounding the issue, Section 3 states that display order runs from one through K for the same user and day, so that a journey in this analysis is a within-day display sequence and any genuine customer journey spanning more than twenty-four hours is structurally unobservable regardless of how many publishers it touches. This would also explain the otherwise surprising absence of any sequence at three or more publishers in programmatic display inventory. The manuscript does not discuss the day scoping of its unit at all, which leaves the headline census unable to distinguish a property of advertising behavior from a property of the release's file layout. Stating the within-day unit explicitly, reporting the distribution of certified sequence lengths, and adding a right-censoring diagnostic would resolve the ambiguity.

1.4 The examined data are a small slice of the release, and the exclusion rule selects on the measured outcome

Two further reconstruction concerns compound the preceding ones. The first is coverage. Section 2 reports that four local files were discovered, two empty and two day-15 files containing 430,834 and 410,100 rows, for a total of 840,934. The CriteoPrivateAds release is documented as comprising on the order of 100 million displays across thirty consecutive days, partitioned by day, so the analysis covers well under one percent of the release and a single day out of thirty. Neither fraction appears in the manuscript, nor any explanation of why a publicly hosted release was analyzed from an incidental local subset, while the abstract, Section 2, and the conclusion all speak of CriteoPrivateAds without qualification. With one day there is no way to check whether day fifteen is anomalous, and the 23,848 publisher identifiers are the publishers of one day's partial traffic rather than the release's publisher universe. The second concern is selection. The manuscript defends its exclusion rule on the ground that publisher, engagement, and sales fields never enter it, concluding that excluded bags are not low-value journeys. The first clause describes the code accurately but the inference does not follow, because a rule can select on an outcome without reading that outcome's column whenever the selection variable is correlated with it. Users whose rows straddle two row shards are mechanically those with more rows, and high-activity users are precisely those most likely to have seen multiple publishers; likewise, longer sequences have more opportunities to contain a gap or to have their opening display fall outside the local files, so the probability of passing Equation (1) decreases in sequence length while publisher multiplicity increases in it. Both clauses therefore select against the outcome being measured. The magnitude is not small: the excluded set is reported as 86.83% single-publisher against the retained set's 99.05%, so the retained-set figure is better understood as a bound on single-publisher prevalence than as an estimate of it. Reporting sequence-length distributions for retained and excluded users, together with the cross-tabulation behind the 5,256 incremental exclusions that the shard clause contributes beyond the 366,176 order violations, would make the selection gradient visible and would let an exogeneity claim be replaced by a bias-direction claim the data can support.

Major Concern Category 2: Inferential Design and the Distinguishability Claim

2.1 Indistinguishability is inferred by accepting a null rather than by testing equivalence

The decision rule in Section 3 is a one-sided superiority test: two outputs are distinguishable only if both the point total variation and the lower endpoint of the paired bootstrap interval exceed the declared margin. Failing that rule is a failure to reject, not a demonstration of equivalence, and the two are not symmetric inferential acts, since a rule constructed to detect separation will fail both when the effect is genuinely below the margin and when the data are too thin to resolve it. To support the claim the manuscript actually makes — that the benchmark cannot separate these rules at the declared credit margin — the authors need the mirror-image construction in which the upper endpoint falls below the margin, which is the standard two-one-sided-tests approach to establishing practical equivalence. Applying that standard to the manuscript's own numbers changes the result for the most important pair, because the first-versus-last-touch interval runs from 0.0049637 to 0.0114548 and its upper endpoint exceeds the margin of 0.01, leaving the data compatible with a true separation that the paper's own standard would call material. For the first-touch-versus-Markov pair the point estimate of 0.0088053 is closer still, and no interval is reported at all because of the corpus-level Markov issue, so the pair with the largest observed separation carries no uncertainty quantification. Section 3 nonetheless describes the finding as stating indistinguishability quantitatively and falsifiably, and the conclusion reports that the data do not distinguish the nine output vectors. Recasting the analysis as an equivalence assessment and reporting a three-way classification of pairs into equivalent, distinguishable, and inconclusive would yield a result that still supports much of the paper's argument while matching the evidence; my expectation from the reported interval widths is that many pairs would land in the first category and that the leading pair would land in the third.

2.2 The bootstrap carries a nominal sample of 2,619 and an effective sample of about twenty-five

The resampling draws complete converting bags, of which there are 2,619, but Section 3 reports that only 25 of them are genuinely multi-publisher. On a single-publisher bag every rule under comparison — first and last touch, first and last click, linear, position, the engagement proxy, allocated Shapley — assigns the entire credit to the same channel, so those 2,594 bags contribute identically to every output vector and contribute exactly nothing to any pairwise difference. The entire between-rule signal, and hence the entire sampling variability of the reported total variation differences, is carried by 25 bags holding 37 sales. A nonparametric bootstrap whose statistic depends on twenty-five units behaves very differently from one with 2,619: the number of informative bags drawn per replicate varies substantially, and the resulting distribution of differences is coarse rather than smooth, which is precisely the regime in which percentile intervals are known to have poor coverage. With 1,000 replicates the 2.5th percentile is determined by roughly the twenty-fifth smallest value, which on a lumpy support can move materially with the seed. Since the headline conclusion turns on whether an endpoint sits above or below 0.01, and the reported endpoint for the leading pair is about fifteen percent above that margin, the stability of that endpoint is not a secondary question. The manuscript reports no diagnostic bearing on it — no statement of the informative subsample, no replicate distribution, no comparison of percentile intervals against bias-corrected and accelerated alternatives, and no demonstration of stability across seeds. Disclosing the effective sample size plainly, raising the replicate count well above 1,000, and showing seed stability would cost little and would substantially firm up the inference.

2.3 The margin is declared without operational grounding and is not invariant to choices the paper calls material

The margin of 0.01 is described as one percentage point of aggregate credit and treated as a fixed standard, but no operational justification is offered for it. The paper's framing is explicitly decision-oriented, yet whether one point of aggregate credit matters depends entirely on the downstream decision, and Diemert et al., whom the authors cite, evaluate attribution choices through bidder utility precisely because credit distance does not translate transparently into decision quality. Without an argument connecting the margin to an operational loss it is a round number doing load-bearing work, and a reader who prefers 0.005 reaches the opposite conclusion from the same table, since several pairs in Appendix A clear that threshold. The second difficulty is that total variation on an aggregate credit vector is not invariant to channel granularity, and the manuscript establishes this itself when it reports that grouping changes coverage-game-vector distance by a factor of 3.07. The mechanism is familiar, in that total variation between distributions spread over 23,848 support points is mechanically compressed relative to the same comparison aggregated to twelve. A margin held fixed while the quantity it bounds is known to scale by a factor of three under a regrouping the paper itself calls material cannot be treated as a neutral standard, and if the pairwise differences in Appendix A scale by anything like that factor under grouping, several would exceed the margin and the second headline would reverse. A sensitivity presentation showing how many pairs are declared distinguishable as the margin varies, together with a full replication of the analysis at twelve channels, would address both halves.

2.4 The distinguishability condition is stated on a functional that may not match the decision

A related conceptual point concerns how the second condition is operationalized. It requires that competing rules produce materially different outputs, which Section 3 implements as a test on aggregate channel-level credit vectors. Aggregate closeness and decision-relevant closeness are different things, however, and two rules can produce nearly identical channel-level aggregates while disagreeing substantially on individual journeys, with the disagreements cancelling in the sum. If the downstream use is channel-level budget allocation, the aggregate is the right functional; if it is per-display bidding or per-journey valuation, both of which the manuscript's own opening invokes when it says attribution outputs feed bidding and policy evaluation, then aggregate distance is the wrong functional and a benchmark could fail the condition as stated while still separating rules on the quantity that matters. There is also a conflation worth guarding against, since the fact that rules agree on a dataset is a joint fact about the dataset and the rules rather than a demonstration that the benchmark is uninformative; a benchmark on which all candidates agree has told the practitioner something useful. The manuscript draws this distinction well in its closing operational paragraph but does not reflect it in how the condition is stated or used. Naming the functional on which distinguishability is assessed, justifying it against the stated downstream uses, and reporting a per-journey dispersion statistic alongside the aggregate would close the gap.

Major Concern Category 3: Theoretical Scope and the Claims Drawn From It

3.1 The paper's own table does not show Shapley winning

The title asserts that Shapley wins by construction, and the abstract explains that evaluating the coverage-game Shapley vector against the constructed target yields zero error by design. But the target actually used throughout the empirical sections is the sales-weighted proxy of Equation (2), not the equal split, and under that target the identity delivers not a zero but the value reported in Table 2 as 0.1408 at raw granularity and 0.0459 at twelve channels. Reading Table 2 as a competition, the coverage-game vector wins neither column: at raw granularity linear and position both score 0.1407, below it, and at twelve grouped channels first touch and first click both score 0.0457 while linear scores 0.0458, all below it. In neither configuration is the Shapley vector closest to the target the paper actually evaluates against. The only configuration in which it would win by construction is the hypothetical one where an evaluator adopts the equal-split target, and Section 5 expressly declines to establish that anyone does, reporting that source inspection finds a coverage-game implementation in the pinned repository but does not establish equal split as an evaluation target, and that the surveyed literature contains no example of the exact target-game pair. The manuscript is therefore in the position of asserting a hazard in its title whose empirical realization its own principal table contradicts. This can be resolved in either of two directions. The narrower is to retitle and rewrite the abstract so the claim is explicitly conditional — that were an evaluator to adopt the equal-split target alongside a coverage-game allocator, the comparison would be vacuous — and to present Table 2 as showing that under the sales-weighted target the hazard does not bind. The more valuable is to establish the antecedent by documenting the pairing somewhere in a public benchmark harness, a library's documentation, or a published comparison. The current intermediate position, where the title asserts the conclusion and Section 5 withdraws its premise, is the one option that should not survive revision.

3.2 The identity's scope is narrow and its coverage of actual practice is not established

Theorem 1 holds for the specific characteristic function of Equation (3), a coverage game over distinct-channel sets with uniform weighting and set membership as the only input, and several features of attribution practice fall outside it. Order is discarded, since the journey enters as a set, yet the entire premise of multi-touch attribution, and of the position, first-touch, last-touch, and Markov rules the paper compares, is that sequence carries information; an order-aware characteristic function need not reduce to equal split. Repetition is likewise discarded, which the authors acknowledge when explaining that the allocated output differs from the Shapley vector precisely because touches repeat. The weighting is uniform, which is what delivers the unweighted rather than the sales-weighted target. And coverage is binary rather than a modelled conversion probability, which is what a model-based Shapley attribution would use. The class to which the warning applies may therefore be small, and the manuscript gives the reader no way to judge its size, because it cites four prior works for the identity without stating which characteristic function any of them employs or whether any is the coverage game. The Zhao, Mahboobi and Bagheri treatment is the most obvious place for that comparison and it is not made, while the Molina, Tejada and Weiss family of game-theoretic attribution models would supply exactly the taxonomy needed to say whether the coverage game is a corner case or a common default. Stating the conditions under which the identity holds, giving at least one explicit counterexample marking the boundary, and classifying the constructions in the cited prior art by characteristic function would let readers calibrate how much of the field the warning covers. It is also worth noting that two of the four prior-art citations are grey literature, a master's thesis and a working paper, for an identity that follows immediately from the linearity axiom and the unanimity-game basis and should therefore cite Shapley's original work directly.

3.3 The operational implications are asserted rather than demonstrated

The closing paragraph makes three claims: that failure of distinguishability means the benchmark does not support ranking attribution rules at the declared margin, that target dependence can reward an allocation construction without demonstrating better decision quality, and that downstream bidding or budget claims need either richer multi-channel data or an independently justified operational objective. The first follows from the analysis subject to the qualifications above. The second and third do not, because both depend on a link between credit-vector distance and decision quality that the manuscript establishes in neither direction. To say that a scoring rule rewards a construction without demonstrating better decision quality presupposes that decision quality is separable and that credit distance fails to track it, which is an empirical proposition on which no evidence is offered; symmetrically, the recommendation that practitioners need richer multi-channel support presupposes that such support would produce operationally meaningful rankings, which is likewise untested. The gap is notable because the authors are unusually well placed to close it. They hold the Criteo Attribution release, they have nine implemented allocation rules, and the cited Diemert et al. work supplies an existing evaluation design that scores attribution choices on bidder utility rather than credit distance. Running the nine outputs through such an evaluation and reporting whether the resulting ordering differs from the ordering implied by distance from the target would convert these assertions into results, confirming the paper's thesis in its strongest form if utility separates rules that total variation does not, and reporting an equally informative finding if it does not. Short of that, a stylized sensitivity analysis asking how large a credit error must be before a budget-allocation decision changes would both ground the operational claims and supply the justification the declared margin currently lacks.

3.4 The audit's reach and the protocol it recommends both outrun what is supplied

Two further framing problems follow from the same source. The first concerns scope. Section 1 states that the authors audit the three conditions on the two public datasets this literature uses, and that framing is what gives the audit reach beyond two files, but the claim is never substantiated and the manuscript's own Section 5 undercuts it: LiDDA and IMA are described as working with marketing-mix-model-derived credit vectors, ALM-MTA as evaluating uplift and grouped AUUC, and the Alibaba systems as evaluating conversion-rate prediction under attribution-derived labels, none of them on the audited datasets. A narrower and defensible claim is available — that Criteo Attribution is the most prominent public dataset carrying attribution labels and is therefore the natural resort for researchers without proprietary data, so its limitations constrain independent and reproducible work — and a short citation survey would convert that from assertion into evidence. The second concerns the protocol. The three conditions are offered as a checklist practitioners should run, and the conclusion asserts the audit is cheap enough to run beforehand, but no condition has a stated pass criterion, no threshold is supplied for what fraction of multi-channel journeys suffices, the second condition's statistic is not scale-invariant and its margin is arbitrary, and the third receives only one worked instance with no general procedure. Approximate target dependence, where a target is correlated with but not equal to a candidate's output, is arguably the more common and more insidious case and receives no treatment at all. Nor is any runtime, cost, or effort estimate given, although the paper's own audit required reconstructing journeys from row shards, implementing nine rules in at least two languages, running exact coalition enumeration, and executing a paired bootstrap. Converting the three conditions into a stated procedure with explicit statistics, sensitivity presentations in place of arbitrary thresholds, a treatment of approximate dependence, and a specification of what an adequate benchmark schema would contain would give the field the tool the paper says it needs.

3.5 The verification apparatus is described in detail but cannot be acted upon

The manuscript states that manifests record input hashes, executed commands, resolved seeds, environment versions, and source commits for both repositories, and that results were regenerated from clean checkouts; readers are directed to a deposited artifact for full precision, to a machine-readable manifest for the twenty-eight per-journey bootstrap intervals and the target-score intervals, and to a pinned commit for the inspected library. Nowhere, however, does a repository address, persistent identifier, or availability statement appear, so none of this can be acted upon. That matters more here than in a typical empirical paper for three reasons. The genre is auditing, and the force of a request that readers accept a critical finding about others' benchmarks depends on the audit itself being auditable. Several consequential numbers exist only in the artifact, including the bootstrap and target-score intervals that a reader would need in order to evaluate the equivalence question raised above. And the manuscript references several implementations whose relationships are not made clear — the repository allocator, the repository, the pinned public library, the actual Rust allocator, and both repositories — so that the cross-implementation agreement figures of 2.78 × 10⁻¹⁷, 3.11 × 10⁻¹⁵ and 1.91 × 10⁻¹², which are presented as independent verification, cannot be assessed for independence without knowing which implementations were compared and who authored each. An availability statement with a persistent identifier, promotion of the interval tables into an appendix, and a short paragraph naming each implementation by authorship and language would resolve all three.

Minor Issues

1. The 6.78-point difference does not describe a like-for-like comparison. Section 2 reports that the complete-bag figure differs from the fragment statistic by 6.78 points. The bag-level difference is 99.0454 minus 92.1946, or 6.85 points; the sales-weighted difference is 99.02 minus 92.27, or 6.75. The figure 6.78 arises only by differencing the bag-level complete value against the sales-weighted fragment value, a mismatch repeated in Section 6 as the 92.27-to-99.05 contrast. In a paper whose argument turns on not conflating populations this is unfortunate, and reporting both like-for-like differences would resolve it.

2. Nine eligible outputs are discussed while Table 2 lists ten quantities. The abstract and Section 3 refer to nine eligible outputs, and Appendix A does carry nine labels, but Table 2 lists ten, the extra being the coverage-game Shapley vector. The reason for its exclusion from the eligible set is inferable from Section 4 but never stated, and one clause would spare the reader a recount. Relatedly, "eligible" itself is never defined, and the manuscript uses "valid," "informative," and "eligible" somewhat interchangeably across Sections 1, 2 and 3.

3. The count of twenty-eight bootstrap intervals is unexplained. Appendix A states that the manifest gives all twenty-eight per-journey-model intervals. Twenty-eight is the number of pairs among eight outputs, consistent with excluding Markov from the paired analysis, but the reader must infer this.

4. A single seed is reported and the replicate count is modest. Seed 20260822 is given, which is good practice, but for a decision rule depending on a tail quantile, one seed and 1,000 replicates are thin. Ten thousand replicates and a demonstration of stability across several seeds would cost little.

5. The Wilson interval rests on an independence assumption the paper elsewhere disclaims. The reported interval of 0.6474 to 1.4054 percent is correctly computed for 25 of 2,619 at the 95% level; I reproduced it exactly. The manuscript insists elsewhere, rightly, that observations are clustered within bags and that filtering is deterministic rather than probability sampling. Labelling the calculation an iid sensitivity is a partial acknowledgment, but a sentence on the direction and likely magnitude of the departure would be more useful than the interval itself.

6. The Markov vector is compared against converting-only quantities. Section 3 notes that Markov uses both converting and non-converting transitions and that its corpus-level vector receives no interval, yet it appears in Appendix A and supplies the headline maximum of 0.008805. Including a corpus-level vector in a matrix of converting-only comparisons is a mismatch the paper flags but does not resolve; at minimum that row and column should be visually distinguished.

7. Table 2 reports no uncertainty on its distances from the target. The manuscript notes that target-score intervals exist in the manifest but shows none. Since the raw-granularity values span only 0.1401 to 0.1427, the table is easy to over-read without them.

8. Appendix A has no grouped-channel counterpart. Given that grouping changes distances by a factor of 3.07, the twelve-channel pairwise matrix is arguably the more decision-relevant table and should appear alongside the raw-granularity one. Relatedly, the choice of the top eleven publishers plus an "other" bucket is not justified, neither in the number nor in the ranking criterion.

9. Several data-handling details are reported without context. Two of the four discovered files are empty, which is noted without comment; the raw channel space is described as 23,848 non-null plus missing without saying whether the missing category is a channel, is dropped, or is distributed, which affects coalition enumeration and normalization; the Criteo stress test mentions parsing textual cost-per-order as float64, implying an undocumented quality issue whose parse-failure rate and handling are unreported; and the selection mechanism for the 20,000 events in that test is not characterized, although the resulting figure of 0.0752 depends on it. That test also sits awkwardly, since it is computed on the dataset the paper has just argued contains no multi-channel journeys, where both targets are degenerate over singletons.

10. The engagement proxy's admissibility and weights both need a sentence. Section 3 correctly flags the proxy as a post-display signal and includes it as an alternative heuristic, but it then enters the nine-way comparison on equal footing with ex-ante allocation rules, and the 4/3/2/1 weighting is asserted without any sensitivity check. Whether a post-hoc signal belongs in a comparison of rules usable for bidding deserves explicit treatment.

11. Table 1's conversion column is undefined. The caption explains the sales weighting and flags the fragment row as a caution but does not say whether the column counts converting bags or conversion events, a distinction that matters given that 3,775 sales attach to 2,619 bags.

12. Structural and presentational points. The manuscript carries no contributions list, so the clearest statement of novelty — that the contribution is the measurement reading placed on a known identity — appears only in Section 4, where a reader may already have mistaken Theorem 1 for the claimed result. Section 5 is titled "Literature scope" but functions as scope limitation and offers no positioning against prior benchmark-auditing work. The operational implication, which is the paper's most forward-looking content, sits as an unlabelled run-on at the end of a limitations section. The proof omits minor bookkeeping about how the player set is defined and how channels appearing in no journey are handled. The allocated output is reported in both tables but left undiagnosed, with no bound or empirical characterization of its relationship to the Shapley vector or either target, even though it is what the repository actually produces. And the manuscript contains no figures at all, although the sequence-length distribution, the retained-versus-excluded comparison, and the bootstrap replicate distributions would each be far more legible as plots than as prose.

Missing and Inadequately Integrated Literature

Cited but Inadequately Integrated

Diemert et al. (2017) is cited twice, once for the Criteo release statistics and once in Section 5 for the observation that an assumed metric favors the bidder built for it, and that observation is dispatched in half a sentence although it is the closest existing statement of the manuscript's own target-independence concern. Diemert and colleagues evaluate attribution choices through bidder utility rather than credit-vector distance, which is precisely the independently justified operational objective the conclusion calls for without specifying. Since the authors hold the same dataset and have nine implemented rules, integrating this work properly and running the corresponding evaluation would convert the paper's operational assertions into demonstrations and would supply the grounding the declared margin lacks. The same work is also the documentation of record for a release whose subsampling and field semantics determine what the event census can mean.

Zhao, Mahboobi and Bagheri (2018) and Molina, Tejada and Weiss (2022) are cited together as prior art for the coverage game and its closed form, but the manuscript never states which characteristic function either employs or whether Theorem 1 applies to it. Since the paper's practical claim is that a specific pairing creates a vacuous comparison, establishing whether the most prominent Shapley-for-attribution references fall inside or outside the theorem's scope is essential rather than optional, and the second work's family of game-theoretic models would supply the taxonomy needed to state how large the covered class is.

Dalessandro, Perlich, Stitelman and Provost (2012) appears in the opening citation bracket and is not revisited, although it argues for grounding attribution in a causal estimand and therefore constitutes the field's prior proposal for what an independently justified target looks like. Anderl, Becker, von Wangenheim and Schumann (2016) is cited among foundational methods but not engaged, despite reporting empirical comparisons of graph-based attribution against heuristic rules on real journey data and despite making the journey-delimitation decisions that the manuscript makes implicitly through its day-scoped, shard-constrained unit. The pinned eeghor/mta repository is the only concrete artifact linking Theorem 1 to practice and is characterized in a single sentence; given its evidentiary weight, a fuller account of what was inspected and how it relates to the authors' own allocator is warranted. Finally, the works surveyed and excluded in Section 5 deserve more than exclusion: a marketing-mix-model-derived credit vector is an alternative answer to the very question the third condition poses, uplift-based evaluation is an instance of scoring against an operational objective, and the conversion-rate benchmark featuring labels under multiple attribution mechanisms is the closest existing work to the manuscript's own project, differing in method rather than subject.

Truly Missing Papers

The CriteoPrivateAd dataset paper (Sebbar et al., 2025) is not cited, although the manuscript's principal empirical analysis runs entirely on that release. It documents the roughly 100 million displays across thirty consecutive days, the day partitioning, the hashing of user, publisher and campaign identifiers, the use of hashed campaign identifiers as an advertiser proxy, and the subsampling of labels to meet target click-through rates together with the reweighting the authors recommend to correct for it. Every one of these bears directly on the manuscript's interpretation: the day partitioning supplies the denominator against which the examined slice should be measured and corroborates the within-day journey unit, the hashing establishes the limits on what channel semantics can be recovered, and the label subsampling raises the question of whether sales counts can carry the accounting weight assigned to them in Equation (2) without the documented correction.

Shapley (1953) is not cited, although the identity in Theorem 1 follows immediately from the linearity axiom and the unanimity-game basis, both introduced there, and the proof in Section 4 invokes exactly those properties. Citing the primary source would also relieve the manuscript of resting its prior-art claim on a master's thesis and a working paper. Lundberg and Lee (2017) is likewise absent, although it is the canonical reference for Shapley-valued attribution in machine learning and would make the coverage game's degenerate behavior legible to the manuscript's target audience as an instance of a general phenomenon. More pointedly, Kumar, Venkatasubramanian, Scheidegger and Friedler (2020) argues that applying the Shapley value to feature importance introduces mathematically formalizable properties that need not align with what one wants from an explanation, and cautions against use outside narrowly constrained settings admitting a clear interpretation. The manuscript's target-dependence concern, that an axiomatically determined value can appear empirically validated when it is in fact fixed by construction, is a direct instance of this argument transplanted from interpretability to attribution, and connecting the two would locate the warning within an established line of criticism rather than presenting it as an isolated finding.

On the empirical and inferential side, three further works are missing. Gordon, Zettelmeyer, Bhargava and Chapsky (2019) compares observational advertising-measurement approaches against fifteen large randomized experiments at Facebook spanning roughly 500 million user-experiment observations and finds that the observational methods frequently fail to recover the experimental estimates even after extensive conditioning; it is the strongest available support for the manuscript's closing position that low proxy-target distance describes benchmark construction rather than recovered causal credit, and it also illustrates the standard of evidence that a selection argument of the kind made in Section 2 is normally expected to meet. Lewis and Rao (2015) establishes that individual-level sales volatility in advertising data is so large relative to campaign effects that informative measurement often demands sample sizes far beyond what is available, with median return-on-investment confidence intervals exceeding a hundred percentage points in width; this is the canonical statement of the power problem the manuscript rediscovers in miniature with its twenty-five informative bags, and it would let the distinguishability failure be presented as an instance of a documented phenomenon. Lakens (2017) is a practical primer on equivalence testing and the two-one-sided-tests procedure, addressing directly the inferential distinction between failing to find a difference and establishing its absence, and adopting its framing would let the authors state their central negative result in a form that supports the weight placed on it.

Finally, Berman (2018) is not cited although it is doubly relevant. It analyzes last-touch and Shapley attribution as publisher compensation mechanisms and shows that the Shapley scheme raises advertiser profits relative to last touch under stated conditions, with both belonging to a family of fixed-externality-share methods. It therefore supplies a worked example of the independently justified operational objective the conclusion calls for, and it demonstrates that allocation rules which look nearly identical in aggregate credit can differ materially in their incentive consequences, which bears directly on the gap between aggregate distance and decision quality.

Reference List

Anderl, E., I. Becker, F. von Wangenheim, and J. H. Schumann. 2016. Mapping the Customer Journey: Lessons Learned from Graph-based Online Attribution Modeling. International Journal of Research in Marketing 33(3):457-474.
Berman, R. 2018. Beyond the Last Touch: Attribution in Online Advertising. Marketing Science 37(5):771-792.
Dalessandro, B., C. Perlich, O. Stitelman, and F. Provost. 2012. Causally Motivated Attribution for Online Advertising. ADKDD 2012:1-9.
Diemert, E., J. Meynet, P. Galland, and D. Lefortier. 2017. Attribution Modeling Increases Efficiency of Bidding in Display Advertising. ADKDD'17:1-6.
Gordon, B. R., F. Zettelmeyer, N. Bhargava, and D. Chapsky. 2019. A Comparison of Approaches to Advertising Measurement: Evidence from Big Field Experiments at Facebook. Marketing Science 38(2):193-225.
Korostil, I. 2024. MTA: Multi-Touch Attribution Library. Repository eeghor/mta.
Kumar, I. E., S. Venkatasubramanian, C. Scheidegger, and S. Friedler. 2020. Problems with Shapley-value-based explanations as feature importance measures. Proceedings of the 37th International Conference on Machine Learning, PMLR 119:5491-5500.
Lakens, D. 2017. Equivalence Tests: A Practical Primer for t Tests, Correlations, and Meta-Analyses. Social Psychological and Personality Science 8(4):355-362.
Lewis, R. A., and J. M. Rao. 2015. The Unfavorable Economics of Measuring the Returns to Advertising. Quarterly Journal of Economics 130(4):1941-1973.
Lundberg, S. M., and S.-I. Lee. 2017. A Unified Approach to Interpreting Model Predictions. Advances in Neural Information Processing Systems 30:4765-4774.
Molina, E., J. Tejada, and T. Weiss. 2022. Some game theoretic marketing attribution models. Annals of Operations Research 318(2):1043-1075.
Sebbar, M., C. Odic, M. Lechine, A. Bissuel, N. Chrysanthos, A. D'Amato, A. Gilotte, F. Horing, S. Nogueira, and M. Vono. 2025. CriteoPrivateAd: A Real-World Bidding Dataset to Design Private Advertising Systems. arXiv:2502.12103.
Shapley, L. S. 1953. A Value for n-Person Games. Contributions to the Theory of Games II:307-317.
Zhao, K., S. H. Mahboobi, and S. R. Bagheri. 2018. Shapley Value Methods for Attribution Modeling in Online Advertising. arXiv:1804.05327.

Conclusion and Path Forward

The project this manuscript undertakes is one the field needs. Benchmark auditing is undersupplied relative to benchmark proposing, the three conditions are a sensible organizing frame, and the authors' willingness to report a negative result and to state repeatedly what their data cannot support is a real virtue that should not be penalized. Theorem 1 is correct and honestly attributed, the numerical verification chain is more careful than is customary, and Appendix A's matrix is internally consistent under the checks I applied, including the exact triangle-inequality decomposition of the first-versus-last-touch distance through the linear allocator and the correct propagation of the first-click offset across rows. The Wilson interval likewise reproduces exactly. The concerns raised here are concentrated not on execution but on the step where analytical choices become empirical claims, and on the distance between what the paper demonstrates and what its title, abstract and conclusion assert. The Criteo event key appears finer than the dataset's own documentation and yields a conversion count an order of magnitude above the documented figure; the channel construct is set at a granularity where singletonhood is close to forced, as the paper's own regrouping results show; the completeness rule cannot detect right truncation and operates on a day-scoped unit that forecloses multi-day journeys; the examined slice is well under one percent of a single day of a thirty-day release; and both clauses of the exclusion rule select on variables correlated with the outcome being measured, so the headline prevalence is a bound rather than an estimate. On the inferential side, indistinguishability is inferred from a test designed to detect its opposite, the effective sample is twenty-five rather than 2,619, and the margin on which everything turns is both ungrounded and not invariant to a regrouping the paper itself calls material. Most sharply, the title's claim that Shapley wins by construction is contradicted by Table 2, where the coverage-game vector finishes behind linear and position at raw granularity and behind first touch and first click at twelve channels, because the target actually evaluated is the sales-weighted proxy rather than the equal split.

None of this is fatal and each concern has a concrete remedy, most of which require no new data. Reporting the Criteo census under all three candidate keys, carrying both channel granularities through every table and appendix, stating the within-day journey unit and adding a right-censoring diagnostic, disclosing coverage as a fraction of the documented release and extending the census across several days, and reporting sequence-length distributions for retained and excluded users would together put the empirical claims on a footing that matches the care evident elsewhere. Recasting the distinguishability analysis as an equivalence assessment with a three-way classification of pairs, disclosing the effective sample size, raising the replicate count and demonstrating seed stability, and presenting margin sensitivity rather than a single declared threshold would do the same for the inference. Aligning the title and abstract with what Table 2 shows, mapping the identity's boundary with an explicit counterexample and a classification of the cited prior art, substantiating or narrowing the scope claim with a citation survey, running the bidder-utility evaluation that the cited literature already supplies a design for, turning the three conditions into a stated procedure that addresses approximate as well as exact target dependence, and adding an availability statement with a persistent identifier would address the framing. The hazard the authors have identified is real, the diagnostic instinct is sound, and the apparatus they have built is most of the way to supporting the claims they want to make. Claiming exactly the scope the analysis supports would make this a considerably more durable contribution, and one much harder to dismiss.